Criteria for considering studies for this review

We carried out this set of reviews in two stages. First, we created a database of all ongoing and completed RCTs of higher versus lower omega-6, ALA, LCn3 and total PUFA with a duration of ≥24 weeks. From this database of relevant studies, we selected RCTs for individual reviews.

Six months was chosen as the minimum duration after considering equilibration of PUFAs into body tissues. Careful work by Browning et al 11 suggests LCn3 supplements equivalent to one portion/week of oily fish reach 95% of maximal incorporation by 5 days for eicosapentaenoic acid (EPA) in plasma phosphatidylcholine (95% CI 0 to 18 days) but by 273 days for docosahexaenoic acid (DHA) into blood mononuclear cells (95% CI 0 to 670 days). While this suggests individual variability, on average, all compartments except blood mononuclear cells had equilibrated by 117 days. The authors stated ’EPA and DHA reached a maximum in platelets in 3–4 weeks and 1–2 months, respectively, and in blood mononuclear cells in 6–9 months’. We chose 6 months (24 weeks) as the minimum duration of intervention to allow equilibration of most body compartments. For specific reviews with outcomes needing additional months for body composition changes to affect health, we set the minimum trial duration at 1 year.

Inclusion criteria for the RCT database

We included RCTs with a duration of ≥24 weeks (≥168 days) of continuous involvement and comparing higher with lower omega-6, omega-3 (ALA or LCn3) and/or total PUFA intakes. We included studies reported as full text, abstracts only, trials registry entries and/or unpublished data. We included cluster-randomised studies with ≥6 clusters. Participants were adults (≥18 years old), but we excluded studies of participants who were pregnant or acutely ill (with diagnosed current cancer, undergoing heart or renal transplantation, with HIV or AIDS, on haemodialysis, with IgA glomerulonephritis or any other renal problem except in diabetes). Our reasoning was to exclude people with conditions that may affect the relationship between polyunsaturated fats and cardiovascular events. Studies were included in the database regardless of reported outcomes.

Interventions could include dietary supplementation, a provided diet and/or advice on diet. Supplementation had to be in oil or capsule form, or as foodstuffs provided, to be consumed by mouth (we excluded enteral/parenteral feeds and enemas). Studies were included if they compared the effect of this intervention with usual diet; no advice; no supplementation or placebo (as appropriate); or with lower omega-3, omega-6 and/or total PUFA intake, so long as they created higher versus lower omega-3, omega-6 or total PUFA arms. We also included trials directly comparing omega-3 with omega-6.

Omega-3 trials could aim to increase LCn3 and/or ALA. LCn3 includes EPA, DHA and docosapentaenoic acid in oily fish, fish, concentrated or algal oils. ALA includes refined ALA or products such as oils with an ALA content of ≥10% of the total fat content, such as linseed (flax), canola (rapeseed), perilla, purslane, mustard seed, candlenut, stillingia or walnut as a food or oil, made into a spreading fat or supplementing another food. Sources and types of omega-3 and omega-6 fatty acids are discussed and defined in supplementary text 1 (supplementary file 4). Omega-6 included linoleic acid (LA), gamma-linoleic acid (GLA), arachidonic acid (AA) or any combination, as a supplement or dietary component high in omega-6, such as sunflower oil. Omega-6 advice, foodstuffs or supplements had to aim to increase or decrease omega-6 intake or, if no clear aim was stated (but implied, such as aiming to provide a ’heart health' or a ’Mediterranean' diet), the intervention had to achieve an increase or a decrease of ≥10% of baseline omega-6. We included trials as increasing total PUFA intake where they stated an aim to increase total PUFA or a dietary component high in total PUFA intake, such as vegetable oil, or where the intervention led to an increase or a decrease of ≥10% of baseline total PUFA.

Studies with multiple risk factor intervention on lifestyle factors, such as weight, smoking, physical activity, or dietary interventions not involving dietary fats, were not included, except where the other intervention was a direct replacement for polyunsaturated fats or the effect of diet or supplementation could be separated from other interventions.

Search methods for identification of studies

We ran two sets of searches on CENTRAL (Cochrane), MEDLINE and EMBASE to 27 April 2017, and on ClinicalTrials.com and the WHO International Clinical Trials Registry Platform to September 2016. We also checked included trials of relevant systematic reviews and wrote to authors of included studies for additional studies and trial data (including unpublished outcome data). The first search strategy for MEDLINE (Ovid) was adapted from Al-Khudairy et al 12 and was also used to locate trials of polyunsaturated fats (see supplementary text 2 in supplementary file 4). The second set of search strategies aimed to locate omega-3 trials and was adapted from Hooper et al 13 (see supplementary text 3, supplementary file 4). These complex strategies were adapted for use in the other databases. The Cochrane sensitivity and precision-maximising RCT filter was applied to MEDLINE (Ovid) and for EMBASE, and terms recommended in the Cochrane Handbook for Systematic Reviews of Interventions were applied.14 To ensure the database is up to date, we re-searched all ongoing trials in December 2018 and included four previously ongoing trials,15–18 adding data on a further 50 239 participants in trials from 1.0 to 7.4 years to dataset 1 (supplementary File 1).

Titles and abstracts located by these searches were downloaded, de-duplicated into EndNote software, assessed as a single set for inclusion in the database and used as the wider study pool from which included studies for individual reviews were selected. Included studies in all identified relevant systematic reviews were checked, and additional publications of included trials were obtained. Attempts were made to obtain full-text translations and/or evaluations of all relevant non-English articles.

Assessment of inclusion

Review methods were based on those of the Cochrane Collaboration.19 Two review authors independently screened titles and abstracts for inclusion into the wider database (using EndNote software) and coded them as ’retrieve' (eligible or potentially eligible/unclear) or ’do not retrieve'. All those coded for retrieval by either reviewer were collected in full text, and two review authors independently screened the full text, assessed studies for inclusion, and identified and recorded reasons for exclusion of ineligible studies (LH and one other reviewer) using an inclusion/exclusion form. We resolved disagreements through discussion or consulted a third reviewer (AA). We identified and excluded duplicates and collated multiple publications and abstracts for each trial (as studies rather than publications were the unit of interest). We recorded selection to allow completion of the Preferred Reporting Items for Systematic Reviews and Meta-Analyses flow diagram. The database was compiled within RevMan software20 in the format of Cochrane Characteristics of Included Studies tables (so additional training was not needed) and transcribed into Word, with references added in EndNote to create the Database.

Inclusion criteria for specific reviews

Database studies were assessed for inclusion into specific reviews. Trials of ≥12 months’ duration were included in CVD, mortality and cancer reviews,1–3 7 where they assessed any of the review’s primary or secondary outcomes (table 1). Trials of ≥6 months were included into the glucose metabolism and diabetes, depression and anxiety, IBD and inflammatory markers, and neurocognitive and functional outcomes reviews,4 6 8 21 22 where they assessed any of the review’s primary or secondary outcomes (table 2). For each study included in a review, all primary, secondary and tertiary outcomes were data extracted.

Data collection and analysis for trials included in at least one systematic review

A data extraction form was designed for this set of reviews and tested by each reviewer on a common ‘training’ study. Two review authors each extracted study characteristics independently in duplicate onto a Word data extraction form (by hand or electronically). Characteristics included bibliographical details, methods (study design, total duration of study, details of any ’run-in' period, number of study centres and location, study setting, withdrawals and date of study), details of participants, interventions, comparators and outcomes, process data (dietary intake or body fat data), trial funding, risk of bias assessments, trial registration data, effect modifiers and adverse events. Dichotomous data from dietary advice studies were extracted at the latest point available in the trial (regardless of the amount of reinforcement of the original dietary message), while dichotomous data from supplemental studies were extracted to the point that supplementation ended, or the trial ended, whichever was earlier. Continuous data were extracted at the latest point available in fixed-term trials, but in studies where participants were followed up for varying durations, participants' data were extracted from the first time point following the mean trial duration. Data from periods following the end of a trial were not used in the meta-analysis. Where papers reported continuous results as change from baseline, we used these data; otherwise, we used data at the latest point available (so long as the change in either arm from baseline was greater than the difference between arms at baseline, to exclude trials with very unbalanced baselines). We did not impute change data.

Disagreements were resolved by discussion and/or a third reviewer (LH or AA). For dichotomous outcomes, we extracted the number of participants in whom an outcome was assessed and the number of participants experiencing the outcome for each study arm. For continuous outcomes, the number of participants assessed, the mean and the variance in each arm were extracted (SDs were calculated from other variance data using the RevMan calculator).

Risk of bias was assessed using the Cochrane Risk of Bias tool23 and two additional domains, independently in duplicate alongside data extraction. We assessed attention bias and compliance as we felt these are important in dietary trials:

1. Random sequence generation (selection bias).

2. Allocation concealment (selection bias).

3. Blinding of participants and personnel (performance bias).

4. Blinding of outcome assessment (detection bias).

5. Incomplete outcome data (attrition bias).

6. Selective outcome reporting (reporting bias).

7. Attention bias (an aspect of performance bias, intervention participants receive more time and/or attention from study and/or health personnel during the trial).

8. Compliance (we considered studies to be at low risk of compliance bias when compliance was assessed, results of compliance assessment were clearly reported for all arms and where most participants appeared to have taken ≥75% of the intended fatty acid dose).

Further details about assessment of each domain are found in supplementary table 1 (supplementary file 4). Compliance data are difficult to interpret and assess in dietary trials, as compliance can be assessed in many ways. These include counting return of unused supplements or foods, participant collection of foods or supplements, intake self-report (including diaries) and/or changes in body measures of fatty acids (eg, fatty acids in plasma cholesteryl esters). For these reviews, we developed an assessment method for compliance that incorporated all these possible assessment methods (detailed in supplementary figure, supplementary file 4). For one review, where trial inclusion relied heavily on compliance evidence, we were stricter, insisting on evidence of differences in body markers of total PUFA or of total serum cholesterol, between intervention and control arms.2

We graded each potential source as high, low or unclear risk of bias and provided details from the study reports, unpublished data and/or author correspondence to justify the judgement. We used this to assess summary risk of bias for each trial.

Summary risk of bias

Supplement or capsule-type trials were considered to be at low summary risk of bias where randomisation, allocation concealment, blinding of participants, and personnel and blinding of outcome assessors were all judged low risk. All other trials were considered at moderate or high risk of bias. A dietary advice or all-food provided-type trial was judged at low summary risk of bias where randomisation, allocation concealment and blinding of outcome assessors were all judged adequate (all others were at moderate or high risk). We originally planned to assess summary risk of bias in the same way for all trials, but the WHO NUGAG expert group requested we assess summary risk of bias slightly differently in different types of trials. Research suggests that poorly concealed allocation is associated with 40% greater effect size, so randomisation and allocation concealment are core items for risk of bias assessment.24 Lack of blinding is associated with smaller levels of bias,25 especially where outcomes are objectively measured,26 as were most of those in our reviews, but small amounts of bias can be important where effect sizes are small.

Measures of treatment effect

Dichotomous data were analysed as risk ratios (RRs) with 95% CIs and continuous data as mean difference (MD) with 95% CIs. Where studies assessed effects using different but comparable scales, we standardised scales so that they presented with a consistent direction of effect (multiplying by −1 as needed) then combined using standardised MDs. Skewed data reported as medians were discussed, and medians were added to relevant forest plots to allow visual comparison of findings (but not pooled).

Where included studies had more than two intervention arms and separate control arms for each intervention arm, the relevant control arm was used for each intervention arm. Where there was a single control group, we combined intervention arms to compare with the single control group or used the single most relevant intervention group (to prevent participants appearing more than once in any meta-analysis). In factorial trials where only one intervention was relevant to our reviews, we used the relevant factorial analysis, but where we were interested in several interventions (cf AlphaOmega and Diet and Reinfarction Trial),27 28 we ensured the two interventions were never combined in the meta-analysis.

To minimise missing data, we attempted to contact authors of included and ongoing RCTs (including those identified only via trials registry entries or conference abstracts), to request data on review outcomes and key methods information. An RCT was included in a review where data on at least one review outcome had been measured (and for dichotomous outcomes, at least one person had experienced the outcome). Due to funding constraints, we were not able to contact all study authors.

Data synthesis

We conducted meta-analyses only when participants, comparisons and outcomes were similar enough to address a sensible question. Primary analyses assessed effects of LCn3, ALA, omega-6 and total PUFA on primary outcomes. Meta-analyses were carried out in RevMan 2014.20 Differences between lower and higher PUFA intake arms were combined across studies using RR or MDs in random-effects meta-analysis. We used a random-effects model because dietary interventions are more complex and heterogeneous than many medical treatments, but we used fixed-effects meta-analysis in sensitivity analyses (to check that our results were robust to differing assumptions). We also carried out sensitivity analyses to assess effects of methodological rigour, retaining only studies at low summary risk of bias, studies at low risk of compliance bias and larger trials (randomising ≥100 participants).

We used I² to measure heterogeneity between trials in each analysis.29 Substantial heterogeneity (I²>50%) was reported, and we explored possible causes using prespecified subgroup analyses. We intended to assess reporting biases using a funnel plot only for forest plots with ≥10 trials; however, we sometimes ran funnel plots on key outcomes with only eight or nine trials (never <8), to assess possible biases.

Subgrouping

We explored potential heterogeneity in the effects of omega-6, ALA, LCn3 or total PUFA on primary outcomes by performing prespecified subgroup analyses for all reviews:

1. Intervention type (dietary advice, supplementary capsules, supplemental foods or all foods provided).

2. Dose of LCn3, ALA, omega-6 and total PUFA (and dose response), where dose was the difference in dose between two arms:

   1. LCn3 intake: ≤150 mg/d, >150 to ≤250 mg/d, >250 to ≤400 mg/d, >0.4 to ≤2.4 g/d, >2.5 to ≤4.4 g/d, >4.4 g/d.

   2. ALA intake: <5 g/d, ≥5 g/d.

   3. omega-6 intake: ≤4%E, >4%E. 

   4. total PUFA: <1%E, one to <2%E, two to <5%E, ≥5%E.

3. Trial duration: 6 to <12 months where included, 12 to <24, 24 to <48 and ≥48 months.

4. Replacement of saturated fatty acids (SFA), monounsaturated fatty acids (MUFA), carbohydrate, other PUFA, nil and unclear.

5. Baseline risk of outcome (categories varied by outcome type).

6. Medication use (≥50% of control group on relevant medication vs <50% on such medication—statins for CVD outcomes, antidiabetics for diabetes outcomes and antidepressants for depression outcomes).

7. Baseline LCn3, ALA, omega-6 or total PUFA intake (as appropriate).

8. Change in the omega-3/omega-6 ratio.

Some reviews included additional subgroups, including participants' sex, participants' age and omega-6 type (LA or GLA). The test for subgroup interactions in Review Manager V.5 was used.20

Interpretation

Outcome data were interpreted as follows:

1. Is there an effect on this outcome? (options: ‘increased risk’, ‘decreased risk’ or ‘little or no effect’). For dichotomous data, RR <0.92 or >1.08 for the highest quality evidence (main analysis and sensitivity analyses) suggested increased or decreased risk (otherwise little or no effect). Presence or absence of an effect was not decided by statistical significance.

2. For continuous outcomes, the effect threshold was a change of ≥5% from baseline, except for measures where effects are clearly cumulative (such as body weight) when ≥2% change from baseline was considered a relevant effect size.

3. Quality of evidence was assessed using GRADE assessment30 (Grading of Recommendations Assessment, Development and Evaluation) for key outcomes, and displayed in summary of findings tables. We used the five GRADE considerations (risk of bias, consistency of effect, imprecision, indirectness and publication bias) to assess quality of evidence as it related to the studies that contributed to the meta-analyses using GRADEpro GDT software.31 We justified decisions on downgrading using footnotes.

4. Quality judgements were interpreted (as suggested by Cochrane) into clear statements about the evidence base (high-quality evidence suggests effect/lack of effect, and moderate-quality evidence suggests a probable effect; for low-quality evidence, there may be an effect, and for very low-quality evidence, any effects are unclear as the evidence is of very low quality).

5. Where there was a suggested effect, the effect size was described using number needed to treat (NNT) or absolute risk reduction (ARR).

Using this method, some small statistically significant findings were considered to have ‘little or no effect’, and larger non-statistically significant findings could suggest increased or decreased risk.

Patient and public involvement

We did not involve patients or the public in this research at any stage.